The physical minimum
When you’re entering a new field, or even after you’ve been there for a while, you eventually need to decide how much to specialize. We’re at a moment in history in which it’s impossible for any one person to know everything about his or her profession, and the most meaningful work tends to occur when we drill down deeply at one particular point. Yet somehow we need to remain generalists, too, if we’re going to have the insight and perspective to use what we find. In his Nobel Prize lecture, the physicist Vitaly Ginzburg summed up this predicament:
In the recent past it was possible to be guided by the requirement “to know something about everything and to know everything about something”…but now, it seems to me, this is no longer possible. At the same time, I am startled and dispirited when young physicists (and sometimes not so young ones) restrict themselves to the knowledge in “their” area and are not informed, if only in a general way, about the state of physics as a whole and its “hottest” areas…It is possible, on the basis of theoretical physics studied in one’s student days, to understand all modern physics, or, more precisely, to understand how matters stand everywhere in physics and be aware of the situation. Every physicist…should simultaneously know, apart from theoretical physics, a wealth of facts from different branches of physics and be familiar with the newest notable accomplishments.
So how do we keep ourselves properly informed about a field that is too complex to grasp in its entirety? We perform a kind of triage, as Ginzburg advises, and focus on the “hottest” areas—the places where important work all but begs to be done in our lifetimes. More specifically, we can make a list. As Ginzburg notes:
At the same time, we in Russia like to quote a certain Kozma Prutkov, a fictitious character, who said pompously, in particular, that “there is no way of comprehending the incomprehensible.” So one has to choose something. And so I took this path: I have made a “list” of the top problems of the day. Any such “list” is admittedly subjective. It is also clear that the “list” should vary with time. Lastly, it is clear that subjects not included in the “list” can in no way be regarded as unimportant or uninteresting…I only suggest some enumeration of the questions that, in my view, every physicist should have at least a superficial idea of. Supposedly less trivial is the statement that this is not as difficult as it might seem at first glance. The time to be spent for this purpose is, I believe, no longer than the time a good student spends preparing for an examination, say, on electrodynamics. Acquaintance with all subjects included in this “list” is what I call the “physical minimum.”
Ginzburg goes on to provide an annotated list of thirty subjects in physics, from “controlled nuclear fusion” to “neutrino physics and astronomy.” (Note that this is a list of problems, not of topics for basic education. For the latter kind of list, Gerard ’t Hooft, another Nobel laureate whom I quoted recently on the subject of how to become a bad theoretical physicist, provides a useful one here.)
And this strategy is worth following no matter what your field happens to be. (As Ginzburg says: “Naturally, this equally applies to other specialties, but I restrict myself to physicists for definitiveness.”) We can’t know everything about it, but we can prioritize, putting together a list of active problems that might benefit from new approaches, and making a point of learning enough about them to recognize any useful ideas on which we happen to stumble. Even the act of writing up the list itself has a way of directing your attention onto what actually matters. When you’re preoccupied solely with what is in front of you, it’s easy to forget about the big issues that your discipline as a whole is confronting. And even if you’re mostly aware of the top ten unsolved problems in your profession, it can be enlightening to extend the list to thirty, as Ginzburg does: there may be something to which you can contribute two-thirds of the way down, which is still pretty high. Obviously, this technique can also be applied on a smaller scale—you can list the problems that present themselves in your current project, your job, or your personal life, and make sure that they’re constantly before your eyes. But it also makes sense to aim as high as possible. There’s a huge incentive in every field to turn ourselves into what Hilaire Belloc memorably called “masters of the earthworm,” in which we spend a lifetime focusing on the one tiny corner that we can claim for our own. And it’s probably necessary. But an awareness of the larger problems is what allows us to select the most promising slice of territory.
Best of all, it enables what the scientist W.I.B. Beveridge called the transfer method, in which ideas from one area are applied to seemingly unrelated problems. It’s perhaps the most fertile source of innovation we have, but it doesn’t happen by accident. It occurs, in fact, when smart people make a list of important problems and keep them continuously in mind. As the physicist Gian-Carlo Rota says, in one of my favorite pieces of advice of any kind:
Richard Feynman was fond of giving the following advice on how to be a genius. You have to keep a dozen of your favorite problems constantly present in your mind, although by and large they will lay in a dormant state. Every time you hear or read a new trick or a new result, test it against each of your twelve problems to see whether it helps. Every once in a while there will be a hit, and people will say: “How did he do it? He must be a genius!”
We can’t all be like Feynman, but we can at least position ourselves to make whatever contributions we can. This means remaining attuned to the meaningful problems that remain unresolved; picking specialties that are likely to matter, rather than counting the spots on a sea urchin’s egg; and being ready to pivot whenever our area of expertise seems useful. In the end, we may all need to be masters of the earthworm. But even a worm can turn.